There has been increasing interest in Mendelian randomization as a way to assess causal effects.^{1–19} The basic idea of this approach is to use a genetic marker that affects a particular exposure and affects an outcome of interest only through the exposure. The effect of the genetic marker on the exposure and on the outcome is then used to back out the effect of the exposure itself on the outcome. Under assumptions described below, this can be done even if the exposure–outcome relation itself is confounded. This approach essentially uses the genetic marker as an “instrumental variable”^{3–5},^{9},10 for the effect of the exposure on the outcome. Under exposure–outcome confounding, where associations between the exposure and the outcome do not themselves reflect causal effects, the Mendelian randomization approach can still estimate these causal effects. The approach is appealing because in many settings the confounding between the exposure and the outcome may be intractable so that causal effects cannot be estimated from observational data using standard regression techniques.

The Mendelian randomization approach, however, itself makes a number of assumptions, and these assumptions are not always carefully evaluated. Stated informally, these assumptions are that (1) the genetic marker is associated with the exposure, (2) the genetic marker is independent of the outcome, given the exposure and all confounders (measured and unmeasured) of the exposure–outcome association, and (3) the genetic marker is independent of factors (measured and unmeasured) that confound the exposure–outcome relation. The second assumption is sometimes referred to as the exclusion restriction; if the genetic marker affects the exposure, then the assumption is also sometimes stated as the genetic marker affects the outcome only through the exposure. In other words, for the assumptions of Mendelian randomization to hold, we need a setting like that of Figure 1A or 1B. The Mendelian randomization assumptions are violated in a diagram like that of Figure 2A or 2B because the genetic marker affects the outcome through pathways other than through the exposure.

If these assumptions do hold, then methods from the instrumental variable literature^{9–11} can be applied to use data on the genetic marker, the exposure, and the outcome to estimate the effect of the exposure on the outcome. It is not necessary to have information on the exposure–outcome confounders themselves to be able to do this. If assumption (1) holds about the variant being associated with the exposure but the association between the genetic marker and the exposure is weak, then the genetic marker is sometimes referred to as a “weak instrument.” Using a weak instrument will often amplify biases owing to any violations in the other two Mendelian randomization assumptions.

Although there may be general awareness that these assumptions must hold in a Mendelian randomization analysis, we believe insufficient attention is paid to evaluating these assumptions and their implications. We will discuss these assumptions and their implications at some length here. We will argue that in a number of genetic contexts these assumptions are not plausible. We will also present three ways to help address some of these assumptions and their potential violations, which we believe would help strengthen inferences from Mendelian randomization analyses.

## EXCLUSION RESTRICTION VIOLATIONS: PATHWAYS, TIME, INTERACTION, MEASUREMENT ERROR, REVERSE CAUSATION, SAMPLE SELECTION, AND LINKAGE DISEQUILIBRIUM

We first highlight ways in which the exclusion restriction might be violated. First, if the genetic marker is not to affect the outcome except through the exposure, then the exposure that is used in the analysis must capture all of the ways that the genetic marker may be associated with the outcome. Consider a setting such as that in Figure 3 where *G* denotes the genetic marker, *X* the exposure of interest used in the analysis, and *Y* the outcome. Let W be some variable that is on the pathway from the genetic marker *G* to the exposure *X*. In this case, if *X* is used as the exposure in the analysis, the Mendelian randomization approach will be biased. This is because the genetic marker affects the outcome through a pathway that does not go through the exposure *X*, namely, *G*→*W*→*Y*. If there were any variable *W* on the pathway from *G* to *X* that also affected *Y*, the Mendelian randomization analysis would be biased.

Consider a closely related scenario (Figure 4). Suppose that the genetic marker affects the outcome only through a particular exposure or phenotype, but that this itself consists of two components (*X*_{1}, *X*_{2}). If only one of these two components, *X*_{1} say, were used in the Mendelian randomization analysis, then there could be substantial bias in the Mendelian randomization estimates of the effect of the exposure on the outcome. Once again, the exclusion restriction is violated: the genetic marker affects the outcome via pathways other than the exposure *X*_{1} used in the analysis. The results of the Mendelian randomization analysis will be biased for the effects of *X*_{1} on Y and also for the effects of (*X*_{1}, *X*_{2}) on *Y*.

A related case in this scenario might be if *X*_{1} and *X*_{2} constitute the exposure of interest at two different times (Figure 5), both of which can affect the outcome Y. If the measurement at only one of the times is used in the analysis, then once again, the Mendelian randomization analysis will be biased.

Many of these points have been acknowledged,^{3},^{5},^{9} but it is not clear that these issues are seriously evaluated and discussed when Mendelian randomization analyses are carried out in practice. It is sometimes claimed that, although the Mendelian randomization assumptions may not hold exactly, the bias resulting from them is likely to be small in comparison with the bias from simply examining the associations between the exposure and the outcome.^{3} Although this claim may hold in some scenarios, it certainly will not hold in all. Violations of the exclusion restriction, such as we have discussed, can in fact lead to substantial biases in Mendelian randomization analysis. We illustrate with an example.

It has recently been established that genetic variants on chromosome 15 affect both smoking behavior (eg, cigarettes per day) and lung cancer. Subsequently, there has been interest as to whether the effects of the variants on lung cancer operate entirely through smoking or whether they might also operate through other pathways. A recent analysis^{20} using lung cancer case-control data to examine whether there were additional pathways (not through increasing cigarettes per day) provided substantial evidence that such pathways were indeed present. The techniques used in this analysis were mediation techniques^{21–23} rather than Mendelian randomization techniques; ie, they did not assume (as Mendelian randomization analysis does) that there were no pathways of the variants on lung cancer except through cigarettes per day. Instead, the techniques were designed to evaluate this assumption. The results of these analyses established the presence of pathways other than through increasing cigarettes per day and showed that, in fact, most effect of the variants on lung cancer were not owing to increasing cigarettes per day. Extensive sensitivity analyses for unmeasured confounding and measurement error confirmed this, and the results have been replicated in three other studies.^{20}

Note, however, that the mediator being evaluated was only cigarettes per day, not all aspects of smoking. The results of the analysis are thus still consistent with the possibility that smoking behavior, taken as a whole, mediates the entirety of the association. Indeed, it has been suggested^{24} that a central means by which the variants affect lung cancer is by increasing the amount of nicotine and toxins extracted per cigarette (eg, through deeper inhalation). This then would be a scenario similar to that depicted in Figure 4, where two aspects of the smoking phenotype (eg, cigarettes per day *X*_{1} and depth of inhalation *X*_{2}) may mediate all of the effect. What happens then if one were to apply Mendelian randomization using only cigarettes per day? The Mendelian randomization assumptions would be violated because there are other pathways from the variants to lung cancer. In this case, as we will see below, the biases can be substantial.

Using the same lung cancer data, the crude association between smoking one pack of cigarettes per day and lung cancer has an odds ratio of 2.6 (95% confidence interval [CI] = 2.3–3.0) controlling for age, sex, and college education. If we apply a Mendelian randomization approach^{19} to these data, taking cigarettes per day as our exposure, we obtain an odds ratio for the effect of a pack of cigarettes per day on lung cancer of 2,180—vastly larger than that from examining the smoking–lung cancer association directly. Although the smoking–lung cancer association may be confounded, it is unlikely that it could be confounded to the degree that would be required for an effect estimate odds ratio of 2,180. In this case, the bias arises in the Mendelian randomization owing to a failure of the exclusion restriction. The estimate is severely exaggerated because the exposure variable used—cigarettes per day—captures only a small part of the effect of genetic variants on the outcome (ie, the exclusion restriction is violated). Moreover, the association between the variant and cigarettes per day is relatively weak, resulting in weak-instrument problems, which amplifies the bias owing to the exclusion restriction violation. The Mendelian randomization estimate for the effect of cigarettes per day on lung cancer effectively divides the variant–lung cancer association by the variant–cigarettes association; because the latter is so small (because cigarettes per day is only one aspect of smoking by which the variants may affect lung cancer), the final Mendelian randomization estimate is biased dramatically upward.

This example also suggests another way in which the exclusion restriction can be violated. The effects of the variants on lung cancer can be understood as an amplification of the effect of each cigarette smoked (because those with the variant extract more nicotine and toxins per cigarette).^{24} This is a form of gene–environment interaction, and indeed, there is strong statistical evidence for such gene–environment interaction (between the variants and cigarettes per day) on both the additive and multiplicative scales.^{20} However, gene–environment interaction (when both the genetic factor and the environmental factor cause the outcome and interact in their effects) itself constitutes a violation of the exclusion restriction. This is because under such gene–environment interaction, the genetic variants affect the outcome not simply through the value the exposure takes. Such interaction corresponds to Figure 2A, not to Figure 1A. Figure 1A requires that once we know the exposure *X*, the genetic marker *G* gives us no further information about the outcome Y. In the presence of gene–environment interaction, this does not hold, and Figure 2A would describe the actual relations. The exclusion restriction is thus again violated, and Mendelian randomization analyses are biased. It is important to keep in mind that gene–environment interaction may depend on how the exposure is defined. If the exposure were defined as all aspects of smoking behavior (or a composite measure of nicotine and toxins extracted), there may be no gene–environment interaction. The genetic variants may affect lung cancer only through the composite of all aspects of smoking behavior. However, when the exposure is defined as cigarettes per day, then gene–environment interaction is present, and the exclusion restriction is violated. Instrumental variable methods allowing for interaction can, in some contexts, be employed,^{25},^{26} but the assumptions underlying the use of standard instrumental variable estimators would, in general, be violated in the presence of gene–environment interaction.

This brings us to yet another potential violation of the exclusion restriction. Consider the diagram in Figure 6, in which the exclusion restriction holds for the true underlying exposure *X*, but the investigator has access only to *X*^{*}, a measure of the exposure subject to measurement error. Here again, the exclusion restriction will, in general, be violated. Some specific exceptions can arise, such as when the exposure *X* is continuous and subject to classical nondifferential measurement.^{3},^{10},^{16},^{17},^{25} However, in other cases, such as with a dichotomous exposure or differential measurement error, Mendelian randomization analyses will be biased. It is moreover possible that the disease itself distorts the measurement of the exposure with an arrow from Y to *X*^{*} in Figure 6. This would introduce yet further bias.

This brings us to yet another possible violation of the exclusion restriction, which is through reverse causation or feedback. Consider the diagram in Figure 7 in which the genetic variant has no effect on the outcome Y_{1} that does not go through the exposure (*X*_{0}, *X*_{1}) but the exposure *X*_{1} is affected by the previous outcome Y_{0}. If in a Mendelian randomization analysis (*X*_{0}, *X*_{1}) is used as the exposure with the outcome Y_{1}, then our Mendelian randomization assumptions will be violated. In this case, the genetic marker *G* is not independent of the outcome Y_{1} conditional on the exposure (*X*_{0}, *X*_{1}) and the confounders U, because conditional on (*X*_{0}, *X*_{1}, U), the variant *G* is still associated with Y_{1} through the path *G*→*X*_{1}←*Y*_{0}→*Y*_{1} that is open, conditional on *X*_{1}. We would thus get biased estimates when using instrumental variable techniques to estimate the effect of (*X*_{0}, *X*_{1}) on Y_{1}. We note that the situation described in Figure 7 is especially worrisome for retrospective case-control studies, where data on the exposure is collected after diagnosis of the outcome.

Violations of the exclusion restriction can also arise owing to the selection of the sample. For example, if interest lies in the effect of *X* on *Y* but the sample was originally collected as part of a case-control study of another disease D and both *Y* and *X* are associated with D (Figure 8), then even though there is no effect of *G* on Y that does not go not through *X*, *G* is still associated with Y conditional on exposure *X* and confounders U because of the conditioning on the status of D. Instrumental variable estimates of the effect of *X* on *Y* will again be biased. Existing case-control studies are increasingly used for Mendelian randomization analyses of traits other than the diseases they were originally designed to study, so this scenario is relevant in practice. Methods for handling Mendelian randomization analyses with such secondary phenotypes are becoming available,^{27} but if the design is ignored when using standard methods, then biased estimates will result.

Finally, consider the diagram in Figure 9 in which another genetic marker *G*_{U}, which also affects the outcome *Y*, is in linkage disequilibrium with the genetic marker *G* used in the analysis. This again constitutes a violation of the exclusion restriction because *G* is not independent of *Y* conditional on *X* and U. That such linkage disequilibrium violates the assumptions of a Mendelian randomization analysis has been noted in principle^{3},^{9} but is seldom discussed in practice. In this case, we could restore the Mendelian randomization assumptions if we could control for the other genetic marker *G*_{U}. However, to entirely avoid such violations, like that in Figure 9, it would be required that there be nothing on the same chromosome as the genetic marker used in the analysis that also affects the outcome, or that all such variables be controlled. This is a strong assumption, and potential violations are numerous. Recent large-scale fine-mapping studies of autoimmune disease, metabolic traits, cancers, and anthropometric traits have all identified risk loci containing multiple correlated alleles that remain statistically significantly associated with these outcomes after mutual adjustment.^{28–32} Moreover, there are many loci that harbor distinct, linked alleles associated with a wide range of phenotypes (eg, the HLA region and the ABO locus).^{33},^{34} As a concrete example, Garcia-Closas et al^{35} report evidence for a variant for body mass index (BMI) in the FTO gene that is strongly correlated with a different variant for breast cancer. If this variant for BMI were used in a Mendelian randomization analysis for the effect of BMI on breast cancer, the Mendelian randomization assumptions would be violated.

Similar violations of the exclusion restriction occur in the presence of population stratification. Although this can be addressed using the standard methods of genomic control employed in genome-wide association studies, or by using family-based studies,^{3},^{4},^{10} such methods are not necessarily being employed in Mendelian randomization studies. Failure to do so would result in a causal diagram similar to that in Figure 9, with biased results.

These points are not new, but are they adequately considered when Mendelian randomization is employed in practice? Violations can potentially lead to substantial biases. When reporting results of a Mendelian randomization analysis, investigators should clearly state the assumptions being made in the context of their specific application and should discuss the plausibility of the assumptions. Investigators should consider and comment on (1) whether the exposure used in the analysis completely captures the phenotype that may mediate the association between the variant and the outcome, (2) whether the exposure is time-varying, (3) whether there may be gene–environment interaction, (4) whether the exposure may be measured with error, (5) whether there may be reverse causation, and (6) whether there may be other genetic markers on the same chromosome that affect the outcome and are correlated with the marker used in analysis. If a good argument can be made against these possibilities, then investigators can more reliably assume that the exclusion restriction holds. These are, of course, all very strong assumptions. Is there another way forward?

### Approach 1—A Return to Katan

The origin of Mendelian randomization analysis is often traced to a letter by Katan.^{1} Katan did not propose using instrumental variable statistical methods to estimate the effect of the exposure on the outcome. Rather, he simply proposed examining the association between the genetic variants and the outcome to test for an effect of the exposure on the outcome. He proposed not using the exposure data at all!

At first, this may be surprising. It would seem that we should be better off making use of the exposure data. However, as discussed in the previous section, one of the challenges in ensuring that the exclusion restriction holds is defining and measuring the exposure in such a way as to avoid incomplete phenotype information (time-varying or otherwise), measurement error, and gene–environment interaction. This will, in general, not be easy to do. However, if all we are interested in is testing for an effect of the exposure on the outcome (rather than estimating the magnitude of this effect), then no exposure information is needed. We need only data on the genetic variant and the outcome. We still need to make the exclusion restriction assumption, that the variant affects the outcome only through the exposure, but we do not necessarily need to fully specify what that exposure is, or collect data on the exposure thus defined. To see this, consider again the diagrams in Figure 1A–B. If there were no effect of the exposure on the outcome (ie, no arrow from *X* to *Y*), then the genetic variant *G* and the outcome *Y* should be unassociated. If there is no arrow from *G* directly to *Y* (ie, if the exclusion restriction holds) and if *G* and *Y* are correlated, then there must be an effect of the exposure *X* on the outcome *Y*. And we can test for this without using data on *X*. This was the approach initially proposed by Katan.

Of course it seems more desirable to obtain estimates of the effect of the exposure on the outcome rather than just to test for the presence of an effect. That is what the instrumental variable methods used in Mendelian randomization analysis purportedly do. However, doing so requires much stronger assumptions. This is because for tests to be valid we need the Mendelian randomization to hold under some definition of the exposure. For valid estimates, we need the Mendelian randomization assumption to hold for the measurement of the exposure for which data is available. The Mendelian randomization assumptions are much less likely to hold for a single measurement of the exposure than they are for a complete characterization of all aspects of the exposure and exposure history. If we had data on the entire history of all aspects of the exposure, then we could potentially again proceed to obtain estimates using causal assumptions no stronger than those involved in the tests. In the absence of such complete exposure data, however, the tests require weaker assumptions than the estimates.

Let us revisit the potential violations of the exclusion restriction in Figures 4–9. Suppose we were to follow the original approach proposed by Katan. Consider Figure 4 with multiple exposure components and suppose we had data only on *X*_{1}. As discussed above, our Mendelian randomization estimates would be biased. However, if we were to simply examine whether there was association between *G* and *Y*, we would still have a valid test of whether there was an effect of phenotype (*X*_{1}, *X*_{2}) on the outcome *Y*. If there was no effect, then we should observe no association between *G* and *Y*. Likewise in Figure 5, with time-varying exposures, we could test whether there were an effect of the exposure (*X*_{1}, *X*_{2}) on the outcome *Y* by testing whether *G* and *Y* were associated. Once again, if there were no effect, then we should observe no association between *G* and *Y*. The difficulties with observing only part of the relevant phenotype vanish. We do not need exposure/phenotype information, and we are protected against the biases described earlier because we are not estimating but rather testing.

Similarly, in the case of gene–environment interaction, if there were some definition of the phenotype such that there was no gene–environment interaction (ie, once the phenotype is known, the genetic marker gives no further information on the outcome) so that Figure 1A or 1B holds for that definition of phenotype rather than Figure 2A or 2B, then we could once again test for an effect of phenotype on outcome, simply by looking at the association between the genetic marker and the outcome. If there were no effect, we should find no association. Note that here we do not even need to know under what definition of the phenotype there would be no gene–environment interaction; we only need to assume that there is one and that, with respect to this definition, the exclusion restriction holds.

Similar conclusions hold in the case of measurement error. If we use the original approach suggested by Katan, measurement error does not cause a problem. In Figure 6, if there is no effect of the true exposure *X* on *Y*, we should find no association between *G* and *Y*. We can do testing without data on *X* without worrying about measurement error in *X*. Similarly with Figure 7, if *X*_{1} and *Y*_{1} were associated only because of reverse causation (ie, because *Y*_{0} affects both *X*_{1} and *Y*_{1}, as in Figure 7, rather than because *X* affects *Y*), then we would find no association between *G* and *Y*_{1} if there were no arrows from (*X*_{0}, *X*_{1}) to (*Y*_{0}, *Y*_{1}).

The approach of Katan is thus robust to many of the sources of bias and exclusion restriction violations considered in the previous section, because no data on the exposure is needed to proceed with testing. The price of this robustness is that we get only tests, not estimates. The approach of using just the genetic marker and the outcome to test for an effect of the exposure on the outcome is, however, not robust to all forms of exclusion restriction violations. In Figure 2 or 3, the exclusion restriction would be violated for the exposure *X*, and both tests (using the approach of Katan) and estimates (using instrumental variable methods) would be biased. Likewise in Figure 8, in which there is selection bias or in Figure 9, in which another variant that affects the outcome is in linkage disequilibrium with the variant used in the analysis, the assumptions are violated, and both tests and estimates will be biased.

Still, tests are often protected when estimates are not (Figures 4–7). Testing with Mendelian randomization can to a certain extent be seen as analogous to intent-to-treat analysis in randomized trials in the presence of noncompliance. In trials with noncompliance, we can still get unbiased estimates of the intent-to-treat effect by simply comparing outcomes according to treatment assignment–this is the effect of treatment assignment. However, if we want to estimate the effect of actually complying with the treatment, then we must take noncompliance into account. This is sometimes done using instrumental variable methods, with treatment assignment taken as an instrument for compliance/treatment taken. Doing so requires making the exclusion restriction assumption (ie, there is no effect of assignment on outcome that does not go through measured treatment taken). We may be worried that such an assumption is violated (owing to mismeasured compliance, partial compliance, or psychological effects of treatment assignment), and so standard practice in randomized trials is to take the intent-to-treat effect as the primary estimate of the study and to make an instrumental variable analysis (or any other analysis using compliance data) as a secondary analysis. This ensures the greatest validity for the primary analysis. The equivalent to the intent-to-treat analysis in Mendelian randomization is to simply look at the *G*–*Y* association, which is the original approach of Katan. Current Mendelian randomization practice is to report instrumental variable estimates as primary, but perhaps, this should be reversed with testing as primary and the instrumental variable estimate as secondary, thereby paralleling practices in randomized trials.

The other thing that is made clear by the approach of Katan is the strength of the assumptions. We are using a test of association between the genetic marker and the outcome to draw a conclusion about the effect of the exposure on the outcome. The assumptions being made, as outlined above, do the rest of the work. It should also be noted that the instrument variable methods themselves could in theory be used only for the purposes of testing. Testing whether the instrumental variable estimate is different from zero constitutes a valid test of the null hypothesis of no association between the genetic variant and the outcome, and thus under the Mendelian randomization assumptions a valid test of the null of no effect of the exposure on the outcome.^{9} Such a test makes no stronger causal assumptions than the approach of Katan. It is when the instrument variable techniques are used to obtain estimates, rather than just tests, that the stronger assumptions (concerning the validity of the exclusion restriction for the actual exposure measured) are required. But if instrumental variable methods are being used only for testing, it is not clear why they would be preferred to the approach advocated by Katan. In using instrumental variable methods, it can seem that the sophistication of the analysis somehow produces the conclusion, whereas in fact, it is relying on assumptions—and even stronger assumptions for estimation.

### Approach 2—Sensitivity Analysis for the Exclusion Restriction and Other Violations

Although the approach of Katan can be helpful in addressing violations of the Mendelian randomization assumptions in Figures 4–7, some of the other violations, such as those in Figures 2, 3, 8, and 9, are still subject to bias. Another approach to help address violations of the Mendelian randomization assumptions is to use sensitivity analysis to assess the extent to which various exclusion restriction violations or assumption violations owing to linkage disequilibrium with another variant affecting the outcome (or population stratification) would bias results and then to try to correct for such bias. The techniques can be adapted in a straightforward manner from existing sensitivity analysis techniques in the literature.^{36–38} We present sensitivity analysis techniques for the approach of Katan; in the Appendix, we discuss how these can also be applied to instrumental variable estimation.

Consider Figure 10, in which we have both a violation of the exclusion restriction (an arrow for *G* to *Y* not through *X*) and linkage disequilibrium (another genetic marker *G*_{U} that was in linkage disequilibrium with *G* and affected the outcome *Y*). Suppose first that the outcome *Y* is dichotomous and we are comparing two levels of the genetic marker *G* (*G* = 0 and *G* = 1). Suppose then that we estimate a risk ratio between *G* and *Y* possibly conditional on measured baseline covariates (which could be approximated by an odds ratio using logistic regression if the outcome is rare). Suppose we assume *G*_{U} is binary and does not interact with *G* on the risk-ratio scale in its effects on *Y* and that *G*_{U} increases the risk of *Y* by a factor of *γ* on the risk-ratio scale. Suppose also that although the exclusion restriction is violated (ie, there is a path from *G* to *Y* not through *X*); that the effects of *G* and *X* on *Y* do not themselves interact on the risk-ratio scale; and that the effect of the direct path from *X* to *Y* is to increase the risk of *Y* by a factor of λ on the risk-ratio scale. Under these assumptions, we can obtain a “corrected” estimate and confidence interval for the association between *G* and *Y* (ie, what we would have obtained had we been able to control for *G*_{U} and had we been able to isolate the *G*→*X*→*Y* path) by dividing our observed estimate and confidence interval by *λ*{1 + (*γ* − 1)*π*_{1}}/{1 + (*γ* − 1)*π*_{0}}^{36},^{38} where *π*_{1} and *π*_{0} are the prevalences of *G*_{U} among those with *G* = 1 and those with *G* = 0, respectively. We could specify values of *λ*, *γ*, *π*_{1}, and *π*_{0} based on previous studies or we could consider a range of these values and vary them in a sensitivity analysis. Doing so would allow one to assess the degree of confounding by another genetic variant and the strength of the exclusion restriction violations that would be required to explain away the association between the genetic variant *G* and the outcome *Y* that is used to test for an effect of the exposure on the outcome. Values of the sensitivity analysis parameters for which the null was still not rejected would be those for which there was still evidence of a causal effect of exposure *X* on outcome *Y*, even though the assumptions themselves were violated.

Likewise for a continuous outcome, *Y*, suppose we estimate the effect of *G* on *Y* on the difference scale, possibly conditional on measured baseline covariates. Suppose we assume *G*_{U} is binary and does not interact with *G* on the additive scale in its effects on *Y* and that *G*_{U} increases *Y* on average by a difference of *γ*. Suppose also that, although the exclusion restriction is violated, the effects of *G* and *X* on *Y* do not themselves interact on the difference scale, and the effect of the direct path from *X* to *Y* is to increase the average value of *Y* by a difference of *λ*. Under these assumptions, we can obtain a “corrected” estimate and confidence interval (ie, what we would have obtained had we been able to control for *G*_{U} and had we been able to isolate the *G*→*X*→*Y* path so that the exclusion restriction was not violated) by subtracting from our observed estimate and confidence interval the factor *γδ* + *λ* where *δ* is the difference in the prevalences of *G*_{U} among those with *G* = 1 and those with *G* = 0, respectively.^{36},^{38} If *G*_{U} is specified as continuous rather than binary, then *γ* can be modified to the effect of a one-unit increase in *G*_{U} on *Y*, and *δ* can be modified to the difference in means of *G*_{U} among those with *G* = 1 versus *G* = 0.^{38} We could again specify values of *γ* and *δ* based on previous studies or we could consider a range of these values and vary them in a sensitivity analysis. Again, doing so would allow one to assess the degree of confounding by another genetic variant and the strength of the exclusion restriction violations that would be required to explain away the association between the genetic variant *G* and the outcome *Y* that is used to test for an effect of the exposure on the outcome.^{36–38} Values of the sensitivity analysis parameters for which the null was still not rejected would be those for which there was still evidence of a causal effect of exposure *X* on outcome *Y*, even though the assumptions themselves were violated.

Although the approach of Katan is subject to bias by linkage disequilibrium with another variant that affects the outcome, as well as to some of exclusion restriction violations, the extent of this bias can be assessed through sensitivity analysis.

### Approach 3—Negative Results May Be More Plausible

The assumptions required for Mendelian randomization are strong, whether for estimation or for testing. The number of applications of Mendelian randomization has been quickly expanding. More attention needs to be paid to its assumptions—to whether incomplete exposure information, time-varying exposures, gene–environment interaction, measurement error, reverse causation, or linkage disequilibrium might bias the analysis. Using the approach of Katan for testing, rather than estimation, circumvents some of these biases but not others. It is in general difficult to establish with much certainty the exclusion restriction that is required in these analyses. Although empirical tests exist to falsify some of these assumptions,^{17},^{25},^{39},^{40} the assumptions cannot be fully empirically verified.

In light of the strength of the assumptions being made, it may turn out that Mendelian randomization analysis is more important for establishing negative results. If there is no association between the genetic variant and the outcome, and if it has already been established that the variant affects the exposure of interest, then this would provide evidence that there is in fact no or very little effect of the exposure on the outcome. Of course, relatively large sample sizes would be needed to establish a null or near-null association with confidence. It would also be necessary to use genetic variants strongly associated with the exposure to avoid weak-instrument problems.^{4} However, research consortia are making it more and more possible to achieve such large sample sizes.

Negative results, like positive results, are potentially subject to biases arising from violations in the assumptions. However, the biases would have to all align perfectly to move the effect estimate to zero when there is in fact a true effect. There is the whole range of nonzero values for false positives to take; there is only one zero value that a false negative may take. A null association, with narrow confidence interval, between a genetic variant and an outcome may thus arguably provide more robust evidence of the negative conclusion of no or very little effect. Such null results can also address important clinical and etiological questions. One recent example is the finding that C-reactive protein-associated variants are not associated with coronary heart disease (suggesting that C-reactive protein is not causally associated with heart disease). Another example are results that indicate that BMI-associated variants are associated with circulating vitamin D levels, whereas variants associated with vitamin D levels are not associated with BMI (suggesting BMI is causally associated with vitamin D levels but not vice versa).^{41},^{42} In light of the strength of the assumptions and the asymmetry between false negative and false positives, Mendelian randomization may in the end prove most valuable in establishing that certain exposures do not affect outcomes, rather than that they do.

## APPENDIX

### Sensitivity Analysis for Violations of the Mendelian Randomization Assumptions When Using Instrumental Variables

Consider Figure 10 in which we have a violation of the exclusion restriction (an arrow for *G* to *Y* that does not go through *X*), as well as linkage disequilibrium (another genetic marker *G*_{U} that was in linkage disequilibrium with *G* and affected the outcome *Y*). Suppose first that the outcome *Y* were dichotomous and *X* continuous and we are comparing two levels of the genetic marker *G*. For simplicity, we denote these by *G* = 0 and *G* = 1, respectively. Suppose that the outcome were rare and that we estimated a risk ratio between *G* and *Y* of *φ*, possibly conditional on measured baseline covariates, and that we estimated the effect of *G* on *X* on the difference scale of *η*, conditional on those same covariates. The standard instrumental variable estimate for the effect of *X* on *Y* on the risk-ratio scale would be *φ*^{1/η}.^{43} Under violations of the exclusion restriction or in the presence of linkage disequilibrium, as in the Figure 10, this would be biased. Suppose we assume *G*_{U} is binary and does not interact with *G* on the risk-ratio scale in its effects on *Y* and that *G*_{U} increases the risk of *Y* by a factor of *γ* on the risk-ratio scale. Suppose also that, although the exclusion restriction is violated, (ie, there is a path from *G* to *Y* not through *X*), the effects of *G* and *X* on *Y* do not themselves interact on the risk-ratio scale, and that the effect of the direct path from *X* to *Y* is to increase the risk of *Y* by a factor of *λ* on the risk-ratio scale. Under these assumptions, we can obtain a “corrected” estimate (ie, what we would have obtained had we been able to control for *G*_{U} and had we been able to isolate the *G*→*X*→*Y* path) by using [(*φ*/*λ*){1 + (*γ* − 1)*π*_{0}}/{1 + (*γ* − 1)*π*_{1}}]^{1/η} where *π*_{1} and *π*_{0} are the prevalences of *G*_{U} among those with *G* = 1 and those with *G* = 0, respectively.^{36},^{38},^{43} Corrected confidence intervals for this expression could be obtained by bootstrapping. We could specify values of *λ*, *γ*, *π*_{1}, and *π*_{0} based on previous studies, or we could consider a range of these values and vary them in a sensitivity analysis.

Likewise, for a continuous outcome *Y*, suppose we estimated the effect of *G* on *Y* on the difference scale of *φ*, possibly conditional on measured baseline covariates, and that we estimate the effect of *G* on *X* on the difference scale of *η*, conditional on those same covariates. The standard instrumental variable estimate for the effect of *X* on *Y* on the difference scale would be *φ*/*η*. Under violations of the exclusion restriction or in the presence of linkage disequilibrium, as in the Figure 10, this would be biased. Suppose we assume *G*_{U} is binary and does not interact with *G* on the additive scale in its effects on *Y* and that *G*_{U} increases *Y* on average by a difference of *γ*. Suppose also that, although the exclusion restriction is violated, the effects of *G* and *X* on *Y* do not themselves interact on the difference scale, and that the effect of the direct path from *X* to *Y* is to increase the average value of *Y* by a difference of *λ*. Under these assumptions, we can obtain a “corrected” estimate (ie, what we would have obtained had we been able to control for *G*_{U} and had we been able to isolate the *G*→*X*→*Y* path so that the exclusion restriction was not violated) by using (*φ* − *γδ* − *λ*)/*η*, where *δ* is the difference in the prevalences of *G*_{U} among those with *G* = 1 and those with *G* = 0, respectively.^{36},^{38} Corrected confidence intervals for this expression could be obtained by bootstrapping. If *G*_{U} is specified as continuous rather than binary, then *γ* can be modified to the effect of a 1-unit increase in *G*_{U} on *Y*, and *δ* can be modified to the difference in means of *G*_{U} among those with *G* = 1 versus *G* = 0.^{38} We could again specify values of λ, *γ* and *δ* based on previous studies, or we could consider a range of these values and vary them in a sensitivity analysis.

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